Treatment Alliance: A Bridge over the Religiosity Gap?

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you for the opportunity to read and comment on this paper. Congratulations on a fine piece of research!

Overall, I found the text compelling, with a research question that piqued my interest due to its relevance and potential impact. The convincing design and clear presentation of results further enhanced the quality of your work. Both the discussion and the reflection on possible implications are differentiated and well-connected to existing research. Moreover, the conclusion is encouragingly relevant for the practice of health care.

Allow me to provide some feedback that might enhance the paper after minor revisions. I have four specific comments that I believe could improve the overall quality of your work even further:

1.  In both the introduction and discussion, you could add some epistemological depth: For a social constructivist, the measurement of "actual" or "objective" religiosity is a challenging concept. You seem to acknowledge this by using quotation marks around these words. Your differentiated way of measuring "objective" religiosity by using a variety of different variables You do not, however, discuss the problems that arise conceptually: religiosity can, for example, be measured through affiliation (quite objectively), by observable behaviour such as prayer or service attendance (less objectively, because the definition of prayer or the attitude towards being at a service can vary a lot) or by self-report of intrinsic religiosity (very subjectively). At the same time, my impression is that the measure's validity becomes stronger the more subjective it is. At the heart of your lacking corelation between "objective religiosity" and "alliance", there might well be an epistemological problem. 

For a more radical constructivist, it would even be hard to accept any difference between "objective" and "perceived" religiosity. 

An explicit discussion of this challenge would take little space, but it might add depth to your paper.

2. You could give more attention to the surprising finding that caregivers with high intrinsic religiosity receive lower alliance ratings from patients with low intrinsic religiosity. The reference to the study on religious interventions by non-religious caregivers does not really convince me, as the constellation is opposite to your finding. However, I would like to read your thoughts on possible explanations. Might high intrinsic religiosity correlate with certain religious styles and different perceptions of religiosity? Might religious professionals overestimate their spiritual care competence?

3. I would like to read your thoughts on the observation (if I understand the results correctly) that professionals rate the alliance constantly higher than the patients. Why is that? 

4. Finally, a comment on the readability of the discussion: You might want to consider subheadings like "Implications" and "Limitations" to divide the discussion section into smaller parts.

Author Response

Thank you for your constructive feedback. Below we will answer the points one by one.

1. Thank you very much for these considerations, which deepen the themes we are researching. It is quite valid to question the actual differences between objective and subjective measurements. Most forms inherently contain a subjective component. In the current study, we have chosen to label the differences observed by researchers based on completed questionnaires as 'objective', and the differences assessed by patients and caregivers themselves as 'subjective'. However, it is justified to acknowledge that even in the first variant, subjective elements are present. We have added a sentence about this in the introduction and a longer section in the discussion. Interestingly, the measures of intrinsic religiosity indeed revealed an association with treatment alliance.

2. This is a relevant question. Religious caregivers may indeed be inclined to adhere to their own perceptions, which could be constraining for patients. Maybe they are less open to different worldviews. They might also overestimate their own competences on spiritual care. We added these possible explanations to the discussion.

3. We have added a section about this in the discussion.

4. That's good advice, thank you; we've followed it. We hope the revised version of the article will meet your expectations!

Reviewer 2 Report

Comments and Suggestions for Authors

This article is well-written and has many virtues. The rationale for this study is clearly articulated and situated with other academic work examining the link between religiosity gap and treatment alliance. The sampling method and psychological measures were also appropriate given the aims of the study. 

My concerns with this manuscript are centered around the statistical analyses. In particular, I don't think that continuous variables should be dichotomized and then used in ANOVA analyses. For instance, I don't agree with the decision to dichotomize intrinsic religiosity scale scores (≥8 "high," <8 "low") to create the objective religiosity gap variable. Categorizing intrinsic religiosity this way is problematic because you lose information (i.e., variation) about participants' intrinsic religiosity. The high-low split prevents you from discriminating between differently (or similarly) scoring participants in the same groups (e.g., the high-low distinction for two different individuals who score 9 and 8, respectively, is arbitrary, given that they have similar scores for intrinsic religiosity). I believe that using intrinsic religiosity expressed as a continuous variable (i.e., in a regression model) is preferable as it will increase statistical power (especially given the small sample size), reduce the number of parameters to be estimated, and would be simpler to interpret (e.g., a change in the predictor variable x corresponds with a change in variable y). Consider computing a difference score using participant instrinsic religiosity minus matched caregiver intrinsic religiosity, and use that score as a continuous predictor variable in a regression. Hence, I think that the current ANOVA analyses using dichotomized continuous variables should be cut and substituted with regression analyses that examine the linear association between religiosity (difference score) and treatment alliance. Further, the authors do not present any quantitative analysis supporting the conclusion that "The association between differences in outlook on life and treatment alliance is mainly a matter of subjectively perceived differences and unmet R/S care needs." This language implies a mediation analysis, which was not used in the present study. For these reasons, I do not recommend publication of this manuscript at this time, unless the authors address the analytical limitations mentioned above.

Author Response

Thank you for the feedback and constructive engagement with the analyses in this article. We have removed the mentioned sentences and hopefully presented the findings more accurately as investigated. Additionally, we appreciate the suggestion to use a difference score of intrinsic religiosity. We had indeed already examined this in a continuous manner in a regression analysis earlier, but encountered a non-linear relationship between the difference score and the WAI. The numbers in the minus sign (-) represent the group of patients where the caregiver has a higher score of intrinsic religiosity than them, while the numbers in the plus sign (+) represent the opposite. The group scoring around zero represents those with little or no 'gap', either religious or secular. We now have chosen to create and use the difference score, including a quadratic term, because indeed this is most accurate. Additionally, we propose to also retain the groups in the article (table 6). We have considered various ways of creating groups: by dividing the ∆ IR scale in three groups for example, but a disadvantage of this would be the overlap in ‘secular match’ and ‘religious match’. Therefore we propose retaining the original groups with a comparison of high and low IR scores, divided by the mean score of 8 in this population. We hope this method of analysis meets your approval. If you have any further questions or suggestions, or if you still prefer to have other groups, based on the ∆IR score, please feel free to let us know.

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

This revision demonstrates a significant improvement, and the addition of the regression analysis strengthens the findings. I endorse the publication of this manuscript.